Dear Colleagues,

First, let's plan to meet together after the wine and cheese on 
Thursday at the Brookhaven meeting.   I will ask Sally about 
an appropriate location, on or off site.

Now to the important point of this message:  I am reporting an 
item from the phone meeting of the Snowmass conveners
that took place today.    There is also homework for you.

Steve Ritz and Jonathan Feng had the idea that it would be useful to 
pose sharp questions for each frontier and for issues that overlap 
frontiers.   They gave this request to their group of Cosmic Frontier
working group conveners.  I attach the list of questions generated
by this exercise as a plain text file.  Some of these 
questions are very sharp.   Steve Ritz characterized them as 

"The questions should produce discomfort, but they should promote 
productive rather than unproductive  discussion."

These questions are mostly on the physics frontiers, but sharp 
questions could also be asked to Instrumentation, Facilities, and 
Computing.

The reaction of the conveners group to these questions was very 
positive.  The general reaction was that Snowmass should try to
provide answers to these questions.  I think that the questions to the 
Energy Frontier groups (HE1-6) enunciate well things that I hear
people asking.  Many of these are issues that your groups are 
already working on.   But it is one thing to have them on your 
list of questions, and it another thing to be told that leaders of 
other Frontiers would like to hear the answers.

The conveners group imagined two uses for such lists of 
questions, first, to bring forward questions that must be addressed
in the working group reports, second, to suggest that sessions at 
the Minneapolis meeting should be devoted to discussion of these
issues.

We were all asked to go to our working group leaders and obtain
similar lists of questions, which could then be merged and 
used in these ways.

So, please begin to make your own lists of sharp questions about 
issues for the future of HEP.    If you send these to me and Chip,
we will assemble the list and iterate it back to the group for approval.
Don't pull punches; if we feel that a question is too harsh, we can 
scale it back in a later iteration.

The due date for completion is mid-April.  Please send your first
round of suggestions soon so that we can discuss a first complied
list when we get together at Brookhaven.

Thank you,

Michael 


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  Michael E. Peskin                           [log in to unmask]
  HEP Theory Group, MS 81                       -------
  SLAC National Accelerator Lab.        phone: 1-(650)-926-3250
  2575 Sand Hill Road                       fax:     1-(650)-926-2525
  Menlo Park, CA 94025 USA              www.slac.stanford.edu/~mpeskin/
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=================================================================
SNOWMASS QUESTIONS from CF [DRAFT LIST, still under construction]

from Jonathan Feng     3/27/13
=================================================================


Steve Ritz:

"The questions should produce discomfort, but they should promote rather than unproductive  discussion."


[Recommend when reviewing the questions to ask how someone could answer them.]

HE All. Is there a realistic scenario in which the US has an onshore energy frontier  machine in the coming 20 years?  If there is, what actions should be taken in the next 5 years?  If there is no such scenario,  how should this impact plans for the coming 20 years?
**be more specific about the options. 

HE All. What is our relationship with CERN for the foreseeable future? Would increasing in-kind contributions (hardware built and managed centrally in the US), be important, and at what level?

HE1.  The message from the LHC seems to be that with data in hand, we consistently outperform expectations for extraction of Higgs properties.  How much is there really for an ILC to contribute?  What key assumptions are we making now that we could relax with ILC inputs?

HE2.  How much do we gain from searches for e.g. triple-gauge-couplings in light of precision electroweak data? Is there any kind of theory where we expect to naturally have SM-like precision measurements, but large deviations in the TGCs?

HE4.  The current data seem to put large amounts of MSSM parameter space in an uncomfortable position.  Clearly some interesting regions remain.  When do we expand to alternatives, such as the NMSSM?  Which ones do we choose?  Are there new paradigms?

HE4: How do we determine experimentally the symmetry  protecting the DM lifetime?

HE5.  What kind of slop is present when we tune tools such as Pythia to handle non-perturbative QCD at colliders?  Do current uncertainty estimations really do justice or are there systematic effects in the modeling/choice of tool that could be larger?  Is it possible we are tuning away subtle interesting and novel effects from new physics? How can we be sure?

HE6.  What is the reasonable target for flavor and CP violation, given no hints for any BSM effects in this direction?

IF3.  What do we learn from neutrino properties in terms of fundamental physics?  To what extent is it worthwhile to spend a large fraction of the US HEP budget in this direction, given the fact that knowing the corresponding quark parameters (which are sometimes over constrained and  testable for consistency)  has not revolutionized our understanding of flavor structure and the matter-antimatter asymmetry, and -- compared with colliders -- relatively few results can be expected?

IF3: If additional resources can be found to restore some of the scope to LBNE, what is the highest scientific priority: moving underground or improving the beam and/or surface detectors?

IF3. In the currently approved configuration for LBNE (assuming no new international support), is LBNE worth doing?  For example, requiring 5 sigma evidence, in which scenarios will it make discoveries (as opposed to confirmations of results from other experiments)?

IF5.  Original motivations to look for light ultra-weakly interacting particles (from dark matter, for example) seem to have largely evaporated.  In light of that fact, is there a motivated parameter
space to aim for?  Does it make sense to look at a next generation of experiments?

IF6: What are some qualitatively interesting thresholds for EDM constraints?  (For example, one might be the predictions of SUSY models with very heavy scalars, but sub-TeV gauginos and Higgsinos.) What experimental program is required to reach these thresholds in the coming 5, 10, 20 years?

CF All: What criteria could be used to prioritize activities across the Cosmic Frontier?  The size of the communities? The connection to other key questions in particle physics and astrophysics?  The variety of possible funding sources?

CF1.  With the significant change of plans involving DUSEL, what are the needs for underground floor space for low-background experiments, and are those needs met in current planing?

CF1.  When is the right time to abandon small projects and band together for larger ones?  Should we already do that now that the DOE has spoken about its G2 plans?

CF1: Dark matter direct detection will reach the neutrino background at some stage.  Although this background is not formally irreducible, is it realistic to think that one could go beyond this?  What experiments would make this possible in a cost-effective way?

CF1: Suppose experiments using one target are significantly more sensitive than those using another target in terms of sigma_SI (say, a factor of 5 or 10 -- you pick.)  Is there a compelling rationale for continuing funding for experiments using the non-leading targets?  How should P5 decide?

CF2: Given large and unknown astrophysics uncertainties (for example, when observing the galactic center), what is the strategy to make progress in a project such as CTA which is in new territory as far as backgrounds go?  How can we believe the limit projections until we have a better indication for backgrounds and how far does Fermi data go in terms of suggesting them?  What would it take to convince ourselves we have a discovery of dark matter?

CF3: Clarify the uncertainties in the expected axion detection rates. Particle physics: for a given mass, what is the lowest possible coupling?  If there is no lower bound, are there values beyond which the models get qualitatively more fine-tuned and the search becomes less
motivated? Astrophysics: can there be large variations local density?  If so, how do these modify the experimental reach?

CF3: What is the target range for axion mass and coupling, and how is that justified?  [This question is being revised.]

CF1/CF2/CF3/CF4: What would it take to convince ourselves that we have: a) a discovery of dark matter?  b) discovered two different species of DM?  c) discovered ALL of the dark matter?  d) a false signal of a dark matter discovery?

CF5.  What are the intrinsic uncertainties in supernovae that limit extractions of the properties of dark energy?  I see statements that we need to observe X number in order to understand these systematics on the measurements, but since such systematics don't seem to be usually quoted as errors (but instead are treated as priors), how do we make the path forward more quantitative?

CF5: What are the roles of optical and CMB observations for particle physics?

CF5: Dark energy experiments are proposed to measure w+1 to higher and higher precision.  Suppose we find w = -1at Stage IV sensitivity?  What are the motivations to plan beyond Stage IV?  Is there a value at which improved precision becomes drastically more difficult to obtain?

CF6/IF4/IF3/HE4: What will it take to identify the mechanism for baryogenesis or leptogenesis?  Are there scenarios that could conceivably be considered to be established by experimental data in the next 20 years?  What experiments are required to achieve this?

CF6: What are the leading prospects for detecting GZK neutrinos? What experimental program is required to do this in the next 5 years, 10 years, 20 years, and how important is this?

CF2/CF6: What are the roles of cosmic-ray, gamma-ray, and neutrino experiments for particle physics?  What future experiments are needed in these areas and why?  Are there areas in which these can have a unique impact?

-------------------------------------------------------------------

additional questions from Jon Rosner


An extended Higgs sector is a universal feature of supersymmetric theories and also occurs in some well-motivated non-supersymmetric schemes.  What are the comparative strengths of (a) precision measurements of couplings of the known state at 125 GeV and (b) direct searches at higher energies? What are the best means to pursue these goals, including via lepton colliders and via high-energy hadron colliders?

Why do we care about the neutrino mass hierarchy?

How does the phase delta in the PMNS matrix describing leptonic CP violation affect the baryon number of the Universe?  If the connection is not direct, can we frame a narrative that describes the importance of delta in an honest way?

Can exclusive bottomonium decays be used to validate PYTHIA tunes?

The existence of dark matter points to some symmetry which guarantees the stability of at least one (possibly more) species.  Can this symmetry, if understood, shed any light on the pattern of quark and lepton masses and mixings?  (This suggests an area of overlap between the Cosmic and Intensity Frontiers which is not represented in the present version of the Venn diagram.)

Are there any other measurements besides w and w' which would shed light on the nature of dark energy?

Is it possible that supersymmetry is realized only at the Planck scale and has something to do with the structure of spacetime itself?  How would we know this?

A light Higgs boson doesn't look good for Technicolor.  Are there viable composite-Higgs models remaining, and what are their signatures?

  



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